These comments repeated verbatim from previous review, errors not fixed: Table 3: The Gibbs energy of W in the upper 3rd column certainly has the wrong sign. The quantity of Cr2O3 in B (5th column, upper section) is manifestly ridiculous. How many other errors are there? Furthermore, evidently the units on the oxides in the upper section are NOT weight percent, since by definition (a) weight percents sum to 100% and (b) you cannot state an extensive quantity such as G in units of Joules for an assemblage defined only by intensive quantities! The units here are grams, except for W which has been renormalized to 100. Only the use of extensive grams allows for a particular value of G and only that allows to sensibly say that the post-equilibration quantity of the oxides in A and B do not separately sum to 100, but in A+B they sum to 200. Grams, not wt %!
Now, one of my major complaints about the previous version was the arbitrary and non-unique set of assumptions needed to define the procedure for finding the final state. The new text is much more explicit about stating that there are assumptions and pointing out what the assumptions are. For example, the key assumption that olivine and orthopyroxene do not nucleate on the eclogite side is explicit now. I think these assumptions are still shaky but, given that they are delineated as assumptions and grounds for future experimental tests, I will allow it. I would prefer that the dependence of the method on the particular choice of independent reactions in the reaction space be acknowledged, or that an argument be provided why the result does not depend on this.
No response to this comment on original manuscript: I note that the imposition of fixed temperature during the three equilibrations is a very particular and not well-motivated choice; it implies the whole system is maintained in thermal equilibrium with an infinite external heat bath. Why not conserve enthalpy, so that if the reactions needed to equilibrate the system are exothermic then it will heat itself up? Why not at least discuss this point?
I still think that Section 2.1, the description of Table 4 and the result of the renormalizing operation is trivial. I can’t tell whether the changes address my comments or not: Of course, if each subassemblage A and B contains at least some quantity of each oxide then the chemical potential of this oxide is fixed and when the systems are considered separately there are no degrees of freedom. The result is pre-ordained. I suppose this could be considered a check that the method of division of W into A and B does not introduce erroneous disequilibrium, but it is no more than that. Likewise, the result in Table 5 and the accompanying conclusion are trivial statements, required by the Gibbs-Duhem theorem, for any correct calculation. And I would say the same about the comparison of Table 6 and Table 7. It is comforting that the calculation given here, while not unique in my opinion, is at least consistent and correct. So, the question (to me) is NOT whether “the observation made for the first studied case with proportion 1:1 can be generalized”. Trivial observations tend to be general. The question is whether the relationship between the results of the 1:1 case and of the 5:1 case can be generalized! Can we find a predictive rule for how these equilibrations change as the original proportions of the unequilibrated subassemblages input to the system are changed? That is the interesting problem.
There isn’t a response either to the problem that, if all chemical components do not diffuse at the same rate, then the conditions that arise in the diffusion couple are NOT on the binary join between the original endmembers, so the original set of ~43 calculations along the binary (how many of them use different starting compositions are not explained anywhere in the text) do not sample the actual composition space that arises. Hence the parameterization of G(*) as a function of f may not describe what happens in the diffusion problem.
Then we come to the key issue of using a diffusion law for G. I wrote before that this is somewhere between impossibly obscure and absolutely incorrect. G is not a conserved quantity, so you cannot write a diffusion equation for it! Derivation of an equation like (6) requires two conditions: that the numerator quantity is conserved (like mass or energy) and that the flux of that quantity is proportional to its gradient (like Fick’s 1st law or Fourier’s law). G obeys neither of these conditions. Unless only reversible processes are allowed (i.e. the system has already been brought to equilibrium), equilibration involves unknown increases in entropy, so dG ≤ -SdT + VdP at constant T and P becomes dG ≤ 0, not dG = 0. And while the mass of each component may diffuse at a rate proportional to the gradient in chemical potential, the chemical potential itself does not do so (unless all activity-composition relations are linear, I guess, which they are not), much less the total Gibbs energy. So why are we talking about a diffusion-couple model for G(*) in the first place? And since, furthermore, we have no kinetic data and are going to assume by fiat that each subsystem is homogeneous and that chemical potentials are uniform across the boundary, what about this problem resembles diffusion in any way?
The new draft includes a response to this in the Conclusions section: “The idea of using the extensive Gibbs free energy function to describe the chemical changes in the 2 sub-systems over time and space is a mean to simplify a problem that otherwise becomes intractable for complex systems. Nevertheless the choice is not a complete abstraction, it is broadly based on the consideration that the mass exchange is not governed by the compositional gradient but by the differences in the chemical potential of the various components in the various phases (e.g. Denbigh, 1971). Ultimately only extensive experimental studies could determine whether the simple transport model applied in this work for the variation of G(∗) in an heterogeneous system can be considered a reasonable approximation for practical geological applications.”
Now, that amounts to admitting that there is no real justification for this method while stating the hope that it might be near enough correct to predict the results of unspecified future experiments. Well, OK, but I posed several well-founded objections, and this text does not address them. How far should we go in allowing a convenient yet formally incorrect procedure in the hopes that it might have some predictive value? That is kind of a judgment call, which I will leave to the editor.
There is also no response to the very important point that this approach appears to enforce the unstated assumption that all components diffuse at the same rate. But that isn’t even remotely true; there are at least order-of-magnitude differences in diffusivities. The actual approach to equilibrium when two lithologies are juxtaposed is locally an open-system problem for each oxide and it explores parts of phase space not explored by the set of input calculations parameterized here. Bottom line: I am not convinced that the 1-D model has any basis in reality or that its results are worth exploring, in detail or otherwise.
No response or change here: If I understand Figure 2 correctly, it apparently disproves the assumption underlying the whole method, because at t = 80 there is olivine (a small amount, admittedly) on the eclogite side of the boundary.
No response or change here: Section 5: The observation that the final state of A changes with mass ratio f, approaching the initial condition for large f, is sort of trivial and well-explained. The complementary observation that that final state of B is quite different from the initial state for all f is based on very incomplete information, since values of f < 1 are not explored. What would we see at f = 0.001? And for the conclusions related to the dynamic system, I am afraid that the calculations explore an inadequate range of the parameter that could be defined by a Peclet number, a ratio of kinetic coefficient S to relative velocity times system size. |

First, thank you for your patience. We've now received additional review of your manuscript. The new reviewer (Anonymous Referee #3) recommends major revision. If you are willing to revise your manuscript, please now prepare a point-by-point rebuttal letter and a revised manuscript.

Mike Heap (Topical Editor of Solid Earth)